Review of Tedesco et al. “Brief communication: Intercomparison study reveals pathways for improving the representation of sea-ice biogeochemistry in models”

The manuscript presents an intercomparison between 6 one-dimensional sea-ice biogeochemical models. Models were forced with the same atmospheric and oceanic data from a time series of observations from a refrozen lead and validated with associated chlorophyll a, nitrate, and silicate data. Models were first run with their default parameterizations, and then teams were asked to tune their models to best match the observations. The authors found that with tuning, most models were able to reproduce chlorophyll a timing and concentration but not so much nutrients. Model teams also differed in their tuning choices.

I think the exercise of model intercomparison is valuable and this is a timely moment to do one for sea-ice BGC, as the number of models has been increasing. I also think the exercise is well-structured and shows significant effort on the part of many people in independently running and tuning the models with the same set of forcings (not a given in other model intercomparisons) in order to reveal a process understanding. As the manuscript is currently written, however, it is difficult for a reader outside of the group to gain much insight or understanding from the exercise. I know this is meant to be a “brief communication”, but I think it deserves a far more detailed paper, for which the changes would probably be considered major revisions.

1.) My main concern surrounds the brief treatment of A) describing what the models are doing and B) usefully synthesizing the outcomes. The manuscript sets up its goal as wanting to gain increased process understanding (rather than simply comparing model outputs, which is more the goal of intercomparisons like Watanabe et al. 2019 that they cite) but I did not feel like it went beyond listing individual model tuning in a way that informed my understanding of the sea-ice ecosystem.

What were key parameter values before/after tuning? Table 2/the list in L178-182 seems like it should be the heart of the Discussion but I didn’t know why modeling teams chose to make those tuning adjustments, whether any choices were specific to model design or previous parameterization, or how model outcomes might be tied to their design. E.g., Can anything be said about models that are BL vs. DE or quota vs. Redfield? Does increased model complexity improve match to observations? Were the tuning changes still within reasonable values for BGC processes, or do they suggest that model physics might be off? What would this work mean for future sea-ice researchers, especially those adjacent to the author group? Lastly, depending on the direction of Discussion, it may be useful to include more model description than currently exists in the Methods. I understand the challenge of summarizing 6 different models, but sometimes there is a place for including key equations.

2.) I would like to see physical variables from both the N-ICE observations and the models (those without prescribed physics). Even though the focus here is on BGC, the ice environment is critical for light and nutrient dynamics and thus for understanding sea-ice algal growth. Please consider adding another plot and adding to the Results and Discussion accordingly. Current places in the writing where the physics were alluded to but could use more backing were L129 and L143-144.

3.) It is near impossible to make sense of the nutrient validation when there is only one time point, which the authors themselves acknowledge (L169-172). Have the authors looked into other time series, such as those from Green Edge, CASES (Cape Bathurst), Resolute Bay, etc.?

The writing itself is generally good and clear. Here are a few line-by-line comments:

L8. Tromso is misspelled.

L37-38. Please consider adding a citation for the claim of significant effects throughout trophic levels.

L51. Please specify that this is maximum algal growth rate.

L67. I feel that for the last sentence of the introduction, this places a lot of emphasis on temporal variability, when your results are also about magnitude. Please consider revising.

L124. Is 83 to 83N correct? If so, please include more details about the drift trajectory.

L164-166. This sentence is relatively redundant for the information that it conveys. Perhaps trim to “Most models exhibited deviations in either phenology or bloom magnitude.”

L194-196. This sentence confused me. Something seems off with the “show to disagree” verb?

L220-221. This statement (“challenges encountering in simulating a refrozen lead”) seems important to understanding the models-observations comparison, but it was never discussed before the Conclusion. Please consider treating this in greater detail in the Discussion.

L230. This is a minor point, but please consider a more common word than “auspicabile”

Figure 1. Please report n for the observations and clarify whether replicates are from different ice cores or technical replicates from the same core.

Table 2. For SIESTA tuning strategy, what does “possibility to keep position” mean?

# General comments

This study provides an intercomparison of six 1D sea-ice biogeochemical models with a focus on the assessment of simulating spring ice algae blooms and associated nutrient variability. The main findings are that: none of the models adequately captured blooms with their default parameters; tuning improved the ice algae blooms but not the nutrient variability; and more systematic tuning strategies are suggested as a next step. I think it is a great effort to conduct an intercomparison study for sea-ice BGC models, which has not been done except for Watanabe et al. (2019). The manuscript is generally easy to follow and clearly structured. However, it would benefit from more careful proofreading to address minor editorial issues and improve overall readability.

The manuscript type is “brief communication”, so I understand that it is written briefly. However, I find it a bit too brief considering the following three points. Therefore, I recommend major revisions and provide suggestions below.

## Physical data. The manuscript lacks the presentation of physical data, even though the text mentions the existence of such data (e.g., L21, L137, L143). Given that physical processes drive the circulation of biogeochemical variables, it seems essential to show the comparison of physical model and observational data, such as snow thickness, ice thickness, and sea surface temperature. With these additions, the study may be able to address (or at least speculate) whether the simulated differences and biases are due to the physical processes.

## Quantitative assessment. Table 2 can be improved by incorporating quantitative findings. Currently, it is a qualitative description that is not very informative and is a bit difficult to follow; one can easily guess the qualitative changes as described in Table 2 (e.g., lower biomass was increased by lowering silica limitation). What would be informative and advance the knowledge is to report the amount of improvements by the amount of parameter adjustments.

## Connection to previous studies. The results and discussion section as well as the conclusions section (L162 onwards) do not appear to contain any reference to previous studies. Hence, it is unclear how this study contributes to the field. This can be achieved by incorporating discussion of the results with previous studies. Specifically, I think that the discussion can be improved by incorporating tuning strategies and intercomparison studies conducted for ocean BGC modelling (e.g., Schartau et al., 2017). Some of these are already mentioned in the manuscript (e.g., L226-234), but it would be better to link these with relevant previous studies to provide a practical direction for future studies.

Schartau et al. (2017). Reviews and syntheses: parameter identification in marine planktonic ecosystem modelling. Biogeosciences.

# Specific comments

L21. “N-ICE2015” is too technical for the abstract. It is better to inform the region and season instead (e.g., north of Svalbard during April-June, 2015).

L22. “tuning” and “adjustments” are used together and they seem to mean the same thing, but this is unclear. I suggest replacing “without tuning, adjustments” by “using their default parameter sets, tuning”.

L23. It would be good to add a sentence here to explain why “adjustments improved biomass simulations but had a limited impact on nutrient representation”. (at least speculate even though the cause is unknown)

L24. It may be informative to add a few words to describe what “harmonised” means here.

L28. Should “ice algae” be “bottom ice” instead, given the following phrase “representing the largest biomass fraction in sea ice”?

L47. “IAMIP1” should be spelled out.

L53. “CMIP6” should be spelled out.

L67. I suggest replacing “existing” by “participating”, as the former sounds like these are all 1D models that exist.

L79. “little” or none? Horizontal advection terms are neglected.

L88. It would be helpful to briefly explain what “dynamic layering” means.

L92. “Chemical Functional Families (CFF)” does not sound familiar in marine BGC modelling. Please use an alternative term or provide a reference.

L124. Please correct the latitudinal range “83 to 83 N”.

L126. It is more intuitive to write the range in an increasing order “80.5 and 81.8 N”.

L139. “Duarte et al. 2017” is one of the participating models in this study? If so, why is the performance poor? Presumably, the model was previously tuned to this study site.

L143. I do not see these physical metrics compared (sea-ice season timing, ice thickness, and snow thickness).

L149. “the extent of biases” will depend on the location where tuning was conducted for the default parameter sets. Hence, it would be helpful to indicate for which region each model was tuned (in Table 1 and/or the text). This will also give an indication for the “portability” of the model (Sec 2.8 of Friedrichs et al. 2007).

Friedrichs et al. (2007). Assessment of skill and portability in regional marine biogeochemical models: Role of multiple planktonic groups, JGR-Oceans.

L158. Please describe the source of the atmospheric forcing used here.

L159. Please specify which model is the one without a thermodynamic component.

L180. “Change in the initial simulation date” seems strange to be considered a tuning parameter.